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Saturday, September 01, 2012

Questioning the Foundations

The submission deadline for this year’s FQXi essay context on the question “Which of Our Basic Physical Assumptions Are Wrong?” has just passed. They got many thought-provoking contributions, which I encourage you to browse here.

The question was really difficult for me. Not because nothing came to my mind but because too much came to my mind! Throwing out the Heisenberg uncertainty principle, Lorentz-invariance, the positivity of gravitational mass, or the speed of light limit – been there, done that. And that’s only the stuff that I did publish...

At our 2010 conference, we had a discussion on the topic “What to sacrifice?” addressing essentially the same question as the FQXi essay, though with a focus on quantum gravity. For everything from the equivalence principle over unitarity and locality to the existence of space and time you can find somebody willing to sacrifice it for the sake of progress.

So what to pick? I finally settled on an essay arguing that the quantization postulate should be modified, and if you want to know more about this, go check it out on the FQXi website.

But let me tell you what was my runner-up.

“Physical assumption” is a rather vague expression. In the narrower sense you can understand it to mean an axiom of the theory, but in the broader sense it encompasses everything we use to propose a theory. I believe one of the reasons progress on finding a theory of quantum gravity has been slow is that we rely too heavily on mathematical consistency and pay too little attention to phenomenology. I simply doubt that mathematical consistency, combined with the requirement to reproduce the standard model and general relativity in the suitable limits, is sufficient to arrive at the right theory.

Many intelligent people spent decades developing approaches to quantum gravity, approaches which might turn out to have absolutely nothing to do with reality, even if they would reproduce the standard model. They pursue their research with the implicit assumption that the power of the human mind is sufficient to discover the right description of nature, though this is rarely explicitly spelled out. There is the “physical assumption” that the theoretical description of nature must be appealing and make sense to the human brain. We must be able to arrive at it by deepening our understanding of mathematics. Einstein and Dirac have shown us how to do it, arriving at the most amazing breakthroughs by mathematical deduction. It is tempting to conclude that they have shown the way, and we should follow in their footsteps.

But these examples have been exceedingly rare. Most of the history of physics instead has been incremental improvements guided by observation, often accompanied by periods of confusion and heated discussion. And Einstein and Dirac are not even good examples: Einstein was heavily guided by Michelson and Morley’s failure to detect the aether, and Dirac’s theory was preceded by a phenomenological model proposed by Goudsmit and Uhlenbeck to explain the anomalous Zeeman effect. Their model didn’t make much sense. But it explained the data. And it was later derived as a limit of the Dirac equation coupled to an electromagnetic field.

I think it is perfectly possible that there are different consistent ways to quantize gravity that reproduce the standard model. It also seems perfectly possible to me for example that string theory can be used to describe strongly coupled quantum field theory, and still not have anything to say about quantum gravity in our universe.

The only way to find out which theory describes the world we live in is to make contact to observation. Yet, most of the effort in quantum gravity is still devoted to the development and better understanding of mathematical techniques. That is certainly not sufficient. It is also not necessary, as the Goudsmit and Uhlenbeck example illustrates: Phenomenological models might not at first glance make much sense, and their consistency only become apparent later.

Thus, the assumption that we should throw out is that mathematical consistency, richness, or elegance are good guides to the right theory. They are desirable of course. But neither necessary nor sufficient. Instead, we should devote more effort to phenomenological models to guide the development of the theory of quantum gravity.

In a nutshell that would have been the argument of my essay had I chosen this topic. I decided against it because it is arguably a little self-serving. I will also admit that while this is the lesson I draw from the history of physics, I, as I believe most of my colleagues, am biased towards mathematical elegance, and the equations named after Einstein and Dirac are the best examples for that.

That's an excellent summary of what I was trying to express with so many words :o)

Do you have an explanation for how we got there? Because it's not really clear to me why the balanced moved. The explanation that lies at hand is that observation is hard to come by, but I'm not sure that's all there is to it. Best,

Time can not be 1D since space is not 1D. In my opinion, there is a lacking of symmetry there. However, any multitemporal theory I do know at present time does not help in order to know if c is the same in the remaining time dimensions or, if it is not, what is its value in those extra time dimensions. We discovered spacetime thanks to electromagnetic waves and the Lorentz invariance EM has, since ultimately c is related to electromagnetic quantities. What about extra c's. We don't know. I wish I could understand multitemporal physics better than 1D physics! Clifford algebras are everywhere, nice to see them in this post. By the way, why don't you tell about your last paper Bee? I think your readers will feel better it you do!

I think it's not that "observation is hard to come by", it's more that there's so much observation, and it's disordered enough that it's extremely hard to organize it under a few straightforward principles, as Einstein was able to do for SR. IMO, as my essay makes a very small and faltering step towards rectifying, our failure better to understand the tools we already have is a significant impediment.

I turned in my own offer late last night (sigh, "of course.") Title:"Can repeated interactions show more about a photon than current theory allows?" It's based on the concept I described at Can we find circularity of a single photon along a range of values?. I consider it a serious chipping at a currently accepted limitation (roughly, projection principle saying we can't find the specific mix of RH and LH states that were in a single photon.) It should be at FQXi in a couple days (my second time there.)

This might sound like a humorous fantasy, but it is not totally:Let's search the space of all GR-SM consistent [and elegant?] mathematical frameworks by computers and let's do the phenomenological study ourselves. Of course, humans will provide the search heuristics.

If I’m to take you correctly, what we need is to have phenomenology lend us a clue as to the reason for our short comings, such that it be able to give us the proper spin on things:-) Levity aside I enjoyed both this post and your FQXi submission. Just as a related thought, the late David Bohm never considered spin to be an intrinsic attribute of a particle, yet rather the consequential translational observed nature of the wave.

”And thought struggles against the results, trying to avoid those unpleasant results while keeping on with that way of thinking. That is what I call 'sustained incoherence.”David Bohm, “Thought as a System”, Routledge (1994) p.11

gooreice 253This "sacrificing" approach strongly reminds me of stochastic methods like "simulated annealing". Randomly deviating from the current situation is a great way to prevent getting stuck in local minima.Creativity guru De Bono called this approach the "intermediate impossible". Using an impossible idea as a temporary stepping stone towards something more practical but previously impossible to imagine.I like it!

But Bee don't you think that the Higgs discovery was the triumph of mathematical consistency and of pure theoretical work in general? And if you continue to climb the same ladder of mathematical and theoretical consistency you will find along the way Supersymmetry, Supergravity and ultimately M-theory. The discovery of the Higgs boosted my optimism for all the well motivated theoretical constructions which exhibit internal mathematical consistency and cohesion. This is why people who failed as physicists and thus hate theoretical physics (do I have to say the name?) were secretly crossing their fingers hoping that the Higgs will not be discovered.

I don't know about physical assumptions, but there is a huge theoretical assumption that is almost certainly wrong. We assume everything can ultimately be understood in terms of a single theory, aka "theory of everything" and that in principle this must be so.

But, as should be clear both from the notion of complementarity as defined by Bohr, AND the extraordinary and probably insurmountable difficulties in reconciling quantum physics with relativity, the ultimate fabric of existence is based on an aporia, and it is this aporia that is fundamental.

What is needed is an understanding of the terms of this aporia rather than futile attempts to overcome it.

We see it as axiomatic on so many levels and the deeper we go into the mysteries the more evident it becomes.

1. Einstein usually said that the Michelson-Morley did not play a role in the development of special relativity, but other observational evidence definitely did.

2. Only towards the end of his life did Einstein turn to mathematical elegance as his primary guide. More typical of his usual approach was: (1) conceptual principles, and decidedly subsequently (2) mathematical formalism.

3. Save that essay theme for another time. Clearly if there have been mistaken assumptions in the theoretical physics of the last 4 decades, one major one was surely the obsession with mathematical formalism. Need I mention stringy theories.

4. Having h-bar as a variable is interesting. Maybe someday people will also dare to question the absolute constancy of G.

"The intuitive mind is a sacred gift and the rational mind is a faithful servant. We have created a society that honors the servant and has forgotten the gift." - Albert Einstein

But Bee don't you think that the Higgs discovery was the triumph of mathematical consistency and of pure theoretical work in general? And if you continue to climb the same ladder of mathematical and theoretical consistency you will find along the way Supersymmetry, Supergravity and ultimately M-theory.

I generally agree with you about your argument of the Higgs being a mathematical extension of the standard model. But my understanding is that the theory was fairly tightly constrained mathematically about the Higgs, except for the exact mass it had to be. Also in retrospect they had the corroboration of all the phenomenological detail in the already discovered bosons and fermions in the SM.

Contrary to what you are saying Supersymmetry is not a sure thing. The lowest energy super partners that were supposed to have shown up at the LHC by now have not shown up. Although I am no expert by any means my understanding is that SS models are getting increasinglymathematicslly ugly as the parameter space is increasingly being disallowed. Part of the problem is that it is such an arcane field that everyone depends on the veracity of the few mathematical experts that understood the original and simplest models of string theory. We now depend on them for telling us it is still mathematically a beautiful thing even after the parameter space has altered the original theory drastically.

It seems to me to be similar to the case of quants in wall street telling us before the crash in 2008 that everything was A-ok. Their humongous salaries depended on their turning a blind eye to to inconsistencies in the tranches of CDOs and CDSs they were selling to their clients. And everybody else wanted to believe the quants because no one likes bad news.

One more thing to ponder. The cosmological constant is tiny but not zero. This is a significant problem for SS. It is an observable capable of blowing the very idea of supersymmetry off the map. No one wants to look at it just like the public didn't want to believe what was going on with Wall Street before the crash. You probably know some similar stories since I understand you live in Greece. I'm not being judgmental. We had exactly the same blindfolds over our eyes in the USA.

Regarding your Bohm quote that speaks about avoiding those unpleasant results and so on. There's something psychologists call cognitive coherence, basically the attempt of making sense of information. If there's information that doesn't seem to fit, the brain has a tendency to ignore it or to make it fit. That's one of the reasons people have a confirmation bias, but it's actually worse than that in that it tells us we're uncomfortable holding conflicting information, even though the resolution of such conflict is at the heart of science. Best,

Well, before you could conclude there was a Higgs you had to find the electroweak interaction, W and Z and so on. I wouldn't count these findings as theoretical work. Instead, it's exactly what I mean: there's phenomenology, there's an update of the theory, there's conclusions drawn from that, a prediction, a test, an update of the theory, and so on. Particle physics is an area where theory and experiment traditionally have worked very well together.

That having been said, I agree that predicting and finding the Higgs was a triumph of mathematical consistency. What I'm saying is that mode of inquiry won't get us arbitrarily far. Did you really just say that M-theory necessarily follows from the standard model? Best,

What strikes me when glancing through the FQXI essays, is the mixture of antipathy against modern research (derided in all sorts of ways), with blatand crackpottery of the grossest sort. It's the kind of things where you don't know whether it's a parody, or seriously meant.

Unfortunately, while "thought provoking questioning foundations" sounds cool it is in fact an open invitation to "anything goes" (while “established research is wrong”). See eg http://fqxi.org/community/forum/topic/1450where almost every sentence is absurd.

The only contribution I spotted so far that makes scientific sense is the one by Mathur. And yes, he is a string physicist. Which leaves me wonder why a internationally well-known resaercher would deliberately seek such a company!

$10,000 might answer some of your questions... It must be difficult for the FQXi folks to find a balance between open-mindedness and scientific quality. At least during the last years I had the impression that they try to err on the side of open-mindedness for the submissions, so the real question isn't what's submitted but how the submissions are ranked. Best,

I'm not saying that SUSY is a sure thing or that M-theory follows from the Standard Model and I agree with Eric that we must be careful and have an open mind. I'm just saying that there is a line of thought here a way of working and generalizing in the particle physics that has been proven very fruitful so far. The main component of this line of thought is mathematical and theoretical consistency in order to construct 'next generation' well motivated theoretical models based on existing knowledge and experimental results. I see SUSY, SUGRA and String theory as the natural heirs of this line of thought. Quantum gravity is a different kind of beast of course but lacking experimental guidance I think following the same successful road is the most promising way for progress.

What I am trying to say is basically that there will be no progress without experimental guidance. You're doing a good job representing exactly the line of thought that I have argued is hindering progress. Yes, susy, string theory and also loop quantization and so on are the natural heirs of this line of thought. But all that thinking isn't sufficient to arrive at the right description of nature. As Arun said above, it's not that these are theories that should not be thought about but the balance with phenomenology is off. Theoretical physics has been inching ever closer to mathematical physics, and I think it's not helpful to our understanding of nature. Best,

I did notice your sentence. I'm not sure though why you think the same doesn't apply to string theory. And, sure, I am publishing my little models and I'm working on it and the response I get is usually of the type "interesting idea" but "very speculative". Though I, ironically, find myself to be too conservative. But then everything is relative. Best,

You mean that yours and others well motivated phenomenological/theoretical work is ignored by your peers just because you don't belong to some dominant circles in your community or because it does not comply with the dominant way of thinking? If such thing is happening is bad of course but I'm an outsider and I don't have a clear picture about it.

No, that's actually not what I am mean. I think it is taken note of, and often used as an alibi, not always quite appropriately. What I am saying is that there are not enough people working on the phenomenology. Best,

It would be interesting to know if the people judging the essays at FQXI know the names and qualifications of the people writing the essays or if they are blocked out. I'd be willing to bet large sums of money (if I had it) that there is significant prejudice in the final judging if they don't block that information. No one today would want to award first place to some nobody, say a non-PhD working in a non physics related job, such as patent clerking, no matter how good the essay.

Can you place a chair, for me, beside the twins. I want to listen to how this evolves.:-)

“... These difficulties can be circumvented by changing the quantization condition ...”

I’m sure that you will find other coworkers to explore this and other ideas.....Quark Matter 2012http://qm2012.bnl.gov/sessionRecordings.asp....“... To understand what happens if the symmetry is broken, we first note that in principle the temperature dependence of the potential is not a quantum effect, it is an in-medium effect ....”.... Its not a particle and its not a wave!!!...

“... Since, in this new phase of matter, the quarks and the gluons are in the asymptotic freedom region,one expects that they interact weakly. So, the perturbative methods can be used for such a system. The asymptotic freedom suggests two procedures for the creation of the QGP : (i) The recipe for the QGP at high temperature. If one treats the quarks and the gluons as the massless noninteracting gas of molecules, such that the baryon density vanishes, the critical temperature which above that, the hadronic system dissolves into a system of quarks and gluons (QGP ) is Tc = 140M eV [9]. However, the modern lattice QCD calculation estimates the critical temperature, Tc , to be about 170 M eV [10] (ii) The recipe for the QGP at high baryon density. At zero temperature, the critical baryon density required the transition to take place in nB ≃ 0.7f m− 3 [9] i.e. four times the empirical nuclear matter density. On these grounds, one should expect to ﬁnd the QGP in two places in the nature: Firstly, in the early universe, about 10−5 s after the cosmic big bang or secondly, at the core of super-dense stars such as the neutron and the quark stars. This new phase of matter can also be created in the initial stage of the little big bang by means of the relativistic nucleus-nucleus collisions in the heavy ion accelerators [5–8]. The critical temperature (critical baryon density) at the zero baryon density (zero tem- perature) has been obtained simply for the non-interacting, massless up and down quarks and gluons in the reference [9]....[9] S. M. Wong, ”Introductory Nuclear Physics”, Wiley-VCH Verlag GmbH and Co. KGaA (2004).”

Best not to get hung up on that too much, Eric. We do what we do, we let other people do what they do, take it or leave it. We persist in realizing our mistakes and inventing new.

There is some crossover of ideas into "real" academic Physics, typically when there is a mathematics-like clarity to something new, less often when an idea is vague enough that one can't imagine how to mathematize it. In case you haven't noticed, some of the wildest stuff comes from academics, and not everyone in the previous FQXi contest prize lists is a down-the-line academic.

Yes, you are right about it being best not to get hung up on these things, just for ones own mental health. But it is true none the less that outstanding minds often have a hard time fitting in with the broader culture and the broader culture then turns it's back on them out of preservation of the status quo.

I think the example of the wildest things coming from many main stream physicists is just an example mostly of a lower standard being applied to the class system that currently exists. You can get away with a lot once you have made the cut with earlier work. But often even superb work gets no credit in today's world if you are not born to be a striver. Sad but true. Ego is 90% of achievement, 9% is luck in terms of the family that you were born into and educational resources available to you. The last 1% is pure brilliance and insight.

Those percentages don't apply to actuall achievements, but more the apportionment of credit to achievements that go down in the history books. Einstein and Dirac were two of that lucky one percent that were brilliant and also didn't depend on having career manipulating egos or being born on third base.

It depends. The Universe is composed of random islands of causality, some of them support well the relativity, some of them support the quantum mechanics, some low-dimensional systems do support the simple compositions of both theories (Dirac, Young-Mills, AdS/CFT, Lie group) so they can serve as a model examples for textbooks. But at most of places close to human observer scale these simple principles simply don't work at all.. Does the surface of bug or human brain appear like quantum wave or vector system of Lie group? Of course not, it's way more complex and dimensional, than every formal theory can handle. IMO event the concept of dimensions is fringe, because the hyperspaces of various dimensionality do penetrate mutually. Every physical law is local by its very nature. At the sufficiently general and nonlocal level there are no rules in the random Universe.

Regarding your essay the quantization of gravity may be achievable in sufficiently low number of dimensions, but this result many not be of practical importance anyway, because such low-dimensional constrains don't exist at the usual places of the universe.

So I can agree with its outcome - but after the physicists should face the consequence and they shouldn't ask the public for another grant money for further attempts in quantization of gravity. These money could be spent more effectively somewhere else. We should therefore define the criterions of the effectiveness of the basic scientific research for not to kill the future achievements prematurely.

/* ..Einstein and Dirac are not even good examples.. Their model didn’t make much sense. But it explained the data...*/

It's entertaining to read about it just from convinced quantum gravitist..;-) But we should ask the principal question, why the mainstream physics converged into pair of essentially four-dimensional theories: the quantum mechanics and general relativity? Why just two and not three or single one?

In context of dense aether model such evolution is not accidental at all - the Universe is random, but its simplification goes trough two infima at the first and last quarters of observable mass/energy distance scale. We may even recognize them easily, because they're describing the behaviour of spherical symmetrical objects (atoms and stars composed of atoms). All the rest of Universe has its symmetry broken in less or higher degree.

So there are really only two models, which enable to describe as large volume of the observable Universe from intrinsic and extrinsic perspectives in as simple way, as possible - no less, no more. If we would attempt to replace them with another theory or combination of theories, you'll face the troubles. In this sense the relativity and quantum mechanics both have a good meaning. But it's indeed a mistake to consider them an universal descriptions of Universe under hope, their deterministic universal reconciliation may be possible somewhere at future.

I like your idea of sacrificing mathematical elegance. A desire for an elegant proof was what stood in the way of proving the four color theorem. On the other hand, you probably should hold on to the unreasonable effectiveness of mathematics or you'll put yourself out of business.

"Einstein was heavily guided by Michelson and Morley’s failure to detect the aether"

I agree with Robert's first point here. Exactly what role the MME played is perhaps not 100% clear, but "heavily guided" is certainly wrong.

Of course, to address a further point, various folks have questioned the constancy of G, Dirac for one. On needs to have a theory with testable predictions which are not falsified. Dirac had a theory with testable predictions, but they were falsified.

"Einstein usually said that the Michelson-Morley did not play a role in the development of special relativity, but other observational evidence definitely did."

This appears to be historically correct, but with an interesting twist. John Stachel (Astr. Nachr. 303 (1982) p.47-53) went through all published and unpublished texts by Einstein on SR up to the mid '20s, and found that without exception the MM experiment, if mentioned at all, is quoted in support of the validity of the relativity principle for electromagnetic phenomena (not as support for the light postulate as is usually claimed nowadays). The original 1905 paper only mentions null experiments in general, without singling out MM.

Stachel suggests that an even stronger influence for Einstein to extend the relativity principle to EM phenomena was the inconsistent explanation of induction, famously described in the first paragraph of the 1905 paper.

Replacing Bee's "heavily guided by experiment" by Robert's "guided by conceptual principles" is enough to reestablish Bee's point here: Einstein is traditionally seen as a prime example of the mathematical model of research, whereas he (at least in the early days) was equally, if not more, guided by physical intuition.

Hi Bee, just found your blog. Very good stuff :-) Thought I'd leave a thought on this particular point --- Carlo Rovelli likes to motivate his work, by saying the opposite: that we do not have a single consistent theory of quantum gravity (he, being of an LQG bent, considers string theory to only approach but not reach that target). Thus, he feels the theoretical research to be justified, in that he is looking for *a* theory, not *the* theory.